Psilocybin-facilitated Smoking Cessation Treatment: A Pilot Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Psilocybin-facilitated Smoking Cessation Treatment: A Pilot Study (NCT01943994), a randomized na study. The primary outcome is Prolonged Abstinence: Biologically Verified Cigarette Smoking Abstinence for 6 Months.

2. Clinical Question

The registry describes a randomized comparative efficacy study conducted under supportive conditions. The central statistical contrast is the observed abstinence count in the psilocybin-assisted group against the count in the nicotine replacement therapy group. The outcome is a participant count, so the primary analysis concerns a binary event: meeting the registry definition of prolonged abstinence or not meeting it.

The clinical question is about this combined treatment approach in the enrolled study population. It does not isolate the contribution of psilocybin from the cognitive behavioral program, supportive setting, or other aspects of participation. The record also posts abstinence outcomes at 3 months and 12 months, which provide additional follow-up context rather than replacing the prespecified primary endpoint.

3. Trial Design

The registry identifies this as a randomized, parallel-group study with no masking. The total enrollment was 82 participants: 42 were assigned to psilocybin-assisted treatment and 40 to nicotine replacement therapy. The study is marked completed, and its phase is listed as NA. The sponsor was Johns Hopkins University. The registry lists a start of 2008-09 and a primary completion date of 2023-05-01.

Both groups were assigned a 13-week cognitive behavioral smoking-cessation intervention. In the psilocybin-assisted group, the planned high dose was administered on the target quit date in week 5. In the nicotine replacement group, a transdermal nicotine patch regimen was to begin on that target quit date. These details describe the intended treatment schedules; the registry record does not give adherence or treatment-delivery summaries.

Because the design was unmasked, participants and study personnel were not described as blinded to group assignment. The registry record does not report further details about sequence generation, allocation concealment, stratification, or the practical procedures used to implement randomization. It also does not report the trial's original sample-size justification or its original statistical analysis plan.

The primary endpoint covers abstinence from the target quit date through the 6-month follow-up, with an initial grace period. The record also includes prolonged abstinence outcomes at the 3-month and 12-month follow-ups. At 12 months, the registry separately reports participants who initially received nicotine replacement therapy and participants who crossed over to psilocybin-assisted treatment. These follow-up groups should not be conflated: the crossover group is reported separately from the original psilocybin group and the remaining nicotine replacement group.

Randomization supports a between-group comparison, but the unmasked design, pilot context, and registry's limited reporting of analysis procedures matter when interpreting the estimates. The record does not report whether all randomized participants were included in each analysis or how missing outcome data were handled.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Period 1: Initial Treatment (6 Months)

Period 2: Optional Cross-over (6 Months)

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Prolonged Abstinence: Biologically Verified Cigarette Smoking Abstinence for 6 Months, measured over From the target quit date to the 6-month follow up.

The primary endpoint is the number of participants with prolonged, biologically verified cigarette smoking abstinence from the target quit date through the 6-month follow-up. The definition allows an initial 14-day grace period. Verification used breath carbon monoxide, urine cotinine, and retrospective self-report. In statistical terms, each participant either met the endpoint definition or did not; the reported values are counts of participants meeting it.

A prolonged abstinence endpoint captures sustained cessation over a follow-up interval rather than a single report of not smoking on one particular day. The biological measures provide checks on self-reported smoking status, while retrospective self-report helps establish the history over the interval. This combination is intended to make the outcome operationally more specific than self-report alone. That general rationale does not establish that any particular verification procedure is error-free.

The endpoint is used to compare the randomized groups on a clinically relevant cessation outcome over the stated follow-up period. Its interpretation depends on the registry definition, including the grace period and the required verification approach. The record does not report further details about thresholds for the biological tests, adjudication of conflicting measures, or handling of incomplete verification. It also does not report how missing follow-up information was classified for this endpoint.

The primary result is therefore evidence about the posted endpoint counts in these study groups, under the registry's definition. It is not a direct measure of every aspect of smoking behavior, treatment adherence, or longer-term outcomes beyond the stated follow-up.

7. Results Posted in the Registry

• Nicotine Replacement Therapy (NRT): 10.0% (4/40) versus 40.5% (17/42) on control; risk difference -30.5 percentage points (95% CI -48.0 to -13.0), risk ratio 0.25 (0.09–0.67); unadjusted two-proportion z-test p = 0.002.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Prolonged Abstinence: Biologically Verified Cigarette Smoking Abstinence for 3 Months

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Nicotine Replacement Therapy (NRT) First, Then Psilocybin-assisted Treatment: 30.0% (12/40) versus 47.6% (20/42) on control; risk difference -17.6 percentage points (95% CI -38.4 to 3.1), risk ratio 0.63 (0.36–1.11); unadjusted two-proportion z-test p = 0.102.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nicotine Replacement Therapy (NRT) First, Then Psilocybin-assisted Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Prolonged Abstinence: Biologically Verified Cigarette Smoking Abstinence for 12 Months

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Nicotine Replacement Therapy (NRT): 0.0% (0/14) versus 35.7% (15/42) on control; risk difference -35.7 percentage points (95% CI -50.2 to -21.2); unadjusted two-proportion z-test p = 0.009.
  • Cross-over to Psilocybin-assisted Treatment: 26.9% (7/26) versus 35.7% (15/42) on control; risk difference -8.8 percentage points (95% CI -31.2 to 13.6), risk ratio 0.75 (0.36–1.60); unadjusted two-proportion z-test p = 0.451.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Nicotine Replacement Therapy (NRT) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cross-over to Psilocybin-assisted Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints extend the abstinence follow-up to 3 months and 12 months. Across these outcomes, the broad pattern is not a uniform set of comparisons with equally clear precision: the posted results generally favor the original psilocybin-assisted group over the nicotine replacement group, while comparisons involving participants who crossed over are less conclusive. These follow-up findings provide context for the primary result, but they do not independently establish that the primary contrast persists unchanged over time.

The secondary outcomes are related to the primary outcome because each concerns prolonged, biologically verified cigarette abstinence from the target quit date through a follow-up point. They differ in follow-up duration and, in the 12-month record, in the composition and size of the reported groups. In particular, the registry distinguishes the original nicotine replacement group from participants who crossed over to psilocybin-assisted treatment. Those groups represent different treatment histories and should not be treated as interchangeable versions of the original randomized comparison.

The registry posts unadjusted comparisons for the secondary outcomes, and the record does not report corresponding sponsor analyses for them. General: when several endpoints or comparisons are examined, the chance of finding at least one apparently strong result by chance can increase. Unless a multiplicity plan is reported, secondary p-values and intervals are best treated as exploratory and interpreted with attention to the full pattern rather than in isolation.

The secondary findings can support questions for further study, especially about persistence over follow-up and how crossover affects interpretation. They should not be used to inflate confidence in the primary estimate or to imply that every follow-up comparison has equal evidential weight. The registry record does not report a prespecified hierarchy among the secondary endpoints or how their results were intended to affect the primary conclusion.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Prolonged Abstinence: Biologically Verified Cigarette Smoking Abstinence for 3 Months
• Prolonged Abstinence: Biologically Verified Cigarette Smoking Abstinence for 12 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: a participant either met the prolonged abstinence definition or did not. The registry reports counts by randomized group. For binary outcomes, a comparison can be expressed using several effect measures, each answering a related but distinct question. The registry's own analysis is a logistic regression odds ratio. The recalculated comparison is an unadjusted risk difference based on the posted counts.

What does a risk difference express?

A risk difference subtracts one group's observed event proportion from the other group's observed event proportion. In the primary recalculation, the comparison is nicotine replacement therapy relative to psilocybin-assisted treatment. The estimate is -0.305. The sign depends on the stated subtraction order, so it is important not to describe the sign without naming which group is subtracted from which. A risk difference is expressed on the probability scale, unlike an odds ratio.

The confidence interval for this recalculated risk difference runs from -0.480 to -0.130. Since the interval is entirely on one side of zero, it is compatible with a directional difference under this unadjusted calculation. This does not remove uncertainty about the magnitude of the difference. General: confidence intervals describe a range of effect values that are reasonably compatible with the data and the assumptions of the method. They are not a guarantee that the true value lies in the interval.

What does logistic regression add?

Logistic regression models the odds of a binary outcome. The registry reports an odds ratio of 6.12, with a 95% confidence interval from 1.99 to 23.26 and p = 0.003. An odds ratio above the equality value indicates higher modeled odds in the first group in the listed group order. Odds are not the same as probability, and an odds ratio is not interchangeable with a risk difference or risk ratio. The registry record does not state the regression covariates, so the reported result should be described as the registry's logistic regression analysis without assuming what adjustments it included.

The unadjusted recalculation and registry analysis are not duplicate calculations of the same measure. Their estimates differ in scale because one is a risk difference and one is an odds ratio; they may also differ in modeling assumptions. For this primary outcome, both reported approaches give a direction favoring higher observed abstinence in the psilocybin-assisted group. This consistency of direction does not make the measures identical, nor does it show that possible biases have been removed.

Why do counts and denominators matter?

The group counts show how many participants met the endpoint, while the group denominators show the number represented in that comparison. For the primary endpoint, the denominators are the randomized group sizes. At other follow-ups, the registry reports different groups or denominators in some places, including a crossover group. Those differences should be interpreted from the specific follow-up record rather than assuming every participant remained in the original comparison group throughout follow-up.

General: binary outcome analyses rely on a clear definition of the event and consistent treatment of participants without observed outcomes. If missing outcomes are handled differently across groups, the resulting comparison can be affected. The registry record does not report the missing-data rule or the analysis population definition. It is therefore not possible to infer from the posted counts alone whether all randomized participants were analyzed as assigned, whether participants with missing assessments were excluded, or whether another rule was used.

What is the role of the p-value?

The unadjusted recalculated p-value is 0.002, and the registry's regression p-value is 0.003. A p-value measures how surprising data at least as incompatible with a specified null model would be if that model and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. Its interpretation also depends on whether the endpoint and analysis were prespecified and whether multiple outcomes or analyses were considered; those details are not fully reported in the registry record.

General: for a binary endpoint, low event counts can make estimates and model-based intervals sensitive to the specific observations. This pilot has relatively few participants and few abstinence events in the nicotine replacement group at the primary endpoint. The uncertainty interval is therefore important alongside the p-value and point estimate. Neither statistical significance nor the observed contrast alone establishes the mechanism responsible for the group difference.

11. Confidence Intervals and Precision

The recalculated primary risk difference is -0.305, with a 95% confidence interval from -0.480 to -0.130. The interval does not include zero, but it spans a substantial range of possible differences. It therefore supports a directional contrast in this unadjusted analysis while leaving uncertainty about the size of that contrast. The estimate should not be treated as exact merely because it is printed to four decimal places; the interval conveys the uncertainty more directly.

The registry's logistic regression estimate is an odds ratio of 6.12, with a 95% confidence interval from 1.99 to 23.26. This interval is wide, so the data are compatible with a range of odds ratios. It does not include the equality value for an odds ratio, but its breadth cautions against placing strong emphasis on the point estimate alone. Because this is an odds ratio, its interval cannot be read as a range of risk differences or abstinence proportions.

General: a confidence interval reflects sampling uncertainty under a specified analysis and its assumptions. It does not capture every source of uncertainty, such as measurement error, unreported analysis choices, selection effects, or differences between this study population and another population. The registry record does not report enough detail to assess all such sources.

The study's pilot scale is important when considering precision. With the posted group sizes and event counts, the point estimate may be more variable than estimates from a larger study. The interval gives a clearer account of that uncertainty than a binary significant or not-significant label. It also does not establish that the same effect magnitude would be observed under different conditions or in a different participant population.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations translate the observed effect into planning scenarios. For binary outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect to detect. These are planning assumptions for the illustrations; the original trial's own design assumptions and sample-size justification are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 31 participants per arm for 80% power and 41 participants per arm for 90% power. Planning for 75% of the observed effect gives 61 participants per arm for 80% power and 81 participants per arm for 90% power. Planning for 50% of the observed effect gives 148 participants per arm for 80% power and 198 participants per arm for 90% power.

In plain language, the 80% power column describes the illustrative group size associated with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions are correct. The 90% power column gives the corresponding illustration for a higher chance of detection. Smaller effects require more participants, which is why the figures increase as the assumed effect becomes a smaller fraction of the observed one.

These are planning illustrations based on the observed effect, not observed power for the completed trial. They do not show that the study was designed with these assumptions, and they do not establish what power the original investigators intended.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.405; treatment proportion p₁ = 0.100; average p̄ = 0.252.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6143 = 1.2040.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5753 = 0.4842.
4. n = (1.2040 + 0.4842)² / (-0.3048)² = 30.7, rounded up to 31 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.404761904761905                          # control proportion
p1 <- 0.1                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1943994)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 31 (80% power), 41 (90% power)
 75% of observed effect: n per arm = 61 (80% power), 81 (90% power)
 50% of observed effect: n per arm = 148 (80% power), 198 (90% power)
power.prop.test: 30.7 
Simulated power at n = 31 per arm: 0.824 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary analysis as logistic regression, with an odds ratio of 6.12, a 95% confidence interval from 1.99 to 23.26, and p = 0.003. The recalculated estimate uses the posted counts to obtain an unadjusted risk difference of -0.305, with a 95% confidence interval from -0.480 to -0.130 and an unadjusted p-value of 0.002. The two estimates are on different scales and should not be compared as if they were alternative values of the same quantity.

The sponsor's result expresses the comparison in odds, whereas the recalculation expresses it as a difference in observed event proportions. The recalculation is not adjusted for any covariates. The registry record does not report the covariates in the logistic model, so the degree or nature of adjustment cannot be described from this record. The reported group order is psilocybin-assisted treatment followed by nicotine replacement therapy for the odds ratio.

Both analyses point in the same direction for the primary outcome: the posted abstinence counts are higher in the psilocybin-assisted group than in the nicotine replacement group. The p-values are similar but arise from different analyses. The sponsor's regression is the registry's reported analysis; the simple recalculation is supplementary descriptive context and does not supersede it.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary abstinence endpoint at the 6-month follow-up and secondary abstinence endpoints at the 3-month and 12-month follow-ups. It also reports more than one group comparison for the 12-month outcome, including a comparison involving the crossover group. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a plan describing how the secondary outcomes should be interpreted alongside the primary endpoint.

General: multiplicity arises when several outcomes, time points, groups, or analyses are examined. Without an adjustment or a prespecified interpretation strategy, the probability of at least one chance finding can be greater than for a single planned test. This does not mean that a reported secondary result is necessarily spurious. It means that unadjusted secondary p-values should be treated as exploratory and not as if each were the sole confirmatory test.

The record does not report how missing outcome data were handled. It does not say whether missing assessments were treated as smoking, excluded, imputed, or handled through another rule. Nor does it report the analysis population definition, such as whether the primary analysis followed intention-to-treat principles or included only participants with evaluable follow-up. The posted counts and denominators should therefore be read as reported, without assuming a missing-data procedure.

The registry also does not report the original statistical analysis plan, detailed randomization procedures, or whether any interim analyses were conducted. Those elements should not be inferred from the final posted results. For the sponsor's logistic regression, the covariates and model diagnostics are not reported. For the recalculated comparisons, the estimates are unadjusted and based only on the posted summary counts.

These reporting gaps limit assessment of the full analytic process, including whether choices were prespecified and how robust results might be to alternative assumptions. They do not invalidate the posted numerical results, but they constrain how strongly the analyses can be characterized beyond the methods explicitly described in the registry.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: suicidal ideation (3.8%), gallstones / gallbladder removal (2.5%).

The registry reports serious adverse event figures separately for the original psilocybin-assisted treatment group, the nicotine replacement therapy group, and the crossover to psilocybin-assisted treatment group. The respective numbers at risk were 42, 40, and 26. Serious adverse events affected 0, 1, and 1 participants in those groups. Deaths were reported as 0 in each group.

The registry also reports other, non-serious adverse events affecting 37 of 42 participants in the psilocybin-assisted treatment group, 31 of 40 in the nicotine replacement therapy group, and 25 of 26 in the crossover group. These counts describe participants affected, not the total number of individual events. The groups differ in their treatment histories, and the crossover group is reported separately.

The top serious adverse event terms listed in the record are Suicidal Ideation at 3.8% and Gallstones / gallbladder removal at 2.5%. The registry extract does not provide enough detail to assign these terms to a specific treatment group or to establish causality. Serious adverse event counts are not a complete account of all possible safety outcomes, and comparisons across groups are limited by the small group sizes and the crossover structure.

17. What the Result Does, and Does Not, Mean

The posted primary results show higher observed prolonged-abstinence counts in the psilocybin-assisted treatment group than in the nicotine replacement therapy group at the 6-month follow-up. The registry's logistic regression and the simple unadjusted recalculation both indicate a directional difference for that endpoint. The intervals convey uncertainty about the size of the comparison, and the recalculated risk difference and reported odds ratio describe different measures.

The finding applies to the study's treatment programs and enrolled population: nicotine-dependent cigarette smokers who had multiple unsuccessful quit attempts and continued to want to stop, with the registry describing participants as healthy apart from nicotine dependence. It does not isolate psilocybin from the cognitive behavioral intervention or other supportive conditions, because both groups received structured behavioral treatment and the randomized programs differed in their medication-related components.

The result does not establish the mechanism of any observed group difference, predict the outcome for an individual participant, or show that the same estimate would apply in other settings. The unmasked design, pilot scale, limited reporting of missing-data procedures and analysis populations, and lack of reported original sample-size assumptions all affect how broadly the estimates can be interpreted. The secondary outcomes add follow-up context but are unadjusted and should be considered exploratory in the absence of a reported multiplicity plan.

The registry's safety data report serious adverse events and deaths by treatment group, as well as other adverse events. Those counts are descriptive and do not by themselves establish whether an event was caused by an intervention. The information should be read as a record of the reported trial outcomes, not as a complete safety assessment or a basis for individual medical decisions.

18. Why This Trial Matters Statistically

This study illustrates several statistical issues that commonly arise in small randomized clinical trials. The primary endpoint is binary, and the same posted counts can be expressed using different measures, such as a risk difference or an odds ratio. These measures answer related but distinct questions, so their values should not be compared directly or treated as interchangeable.

The contrast between the registry's logistic regression and the unadjusted recalculation also shows why the analysis method matters. One is a model-based odds comparison; the other is a direct comparison of group event proportions. Without details about the regression covariates and the original analysis plan, readers should distinguish what the record reports from what can be independently calculated from the posted counts.

Precision matters alongside the direction of an effect. The primary interval is compatible with a range of risk differences, and the sponsor's odds-ratio interval is also broad. A p-value alone cannot communicate the range of effect sizes compatible with the data. In a pilot study with limited participant numbers, the estimates provide preliminary evidence and useful planning information, but they do not establish a precise effect magnitude.

The follow-up structure raises additional questions about time points, multiple comparisons, missing data, and crossover. The record's secondary comparisons are not accompanied by a reported multiplicity plan, and the analysis population and missing-data handling are not reported. These are not peripheral details: they influence what the posted estimates can support and how confidently comparisons across endpoints can be interpreted.

Finally, the sample-size illustrations demonstrate how planning requirements depend on the effect size one wants to detect. Smaller assumed effects require more participants. Such illustrations can inform future study planning, but they are not evidence of the original design rationale or of the completed study's observed power.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record describes a pilot study, with 82 participants enrolled and no masking. The primary group sizes were 42 and 40, and the number of participants meeting the endpoint was limited, particularly in the nicotine replacement group. These features contribute to uncertainty and make the estimated magnitude vulnerable to variation in a small dataset.

The trial compared treatment programs rather than isolating a single component. Both groups received the 13-week cognitive behavioral intervention, while the medication-related treatment differed. The unmasked design could also affect participant expectations, treatment engagement, or reporting, although the registry record does not establish that any such effect occurred.

At 12 months, the registry reports a separate crossover group, and the group sizes differ from the original randomized allocation. This structure complicates interpretation of longer-term comparisons as simple comparisons by original assignment. The record does not explain the crossover process, timing, or how it was incorporated into the analysis.

Several methodological details are not reported in the registry record: the original sample-size justification, detailed randomization procedures, the sponsor model's covariates, analysis population definitions, handling of missing outcomes, and a multiplicity plan. The registry also does not report whether interim analyses were conducted. These omissions limit evaluation of prespecification, analytic robustness, and potential bias.

The posted safety figures are descriptive counts and do not provide detailed event narratives, causal assessments, or complete group-specific explanations for the listed serious adverse event terms. The record's summaries cannot resolve whether observed events were related to study treatment. These limitations should be kept in view when interpreting both efficacy and safety results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Psilocybin-facilitated Smoking Cessation Treatment: A Pilot Study — NCT01943994.
• Registry record last updated 2025-05-25; status last verified 2025-05.
• Results first posted 2024-07-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The completed randomized, unmasked, parallel-group pilot study enrolled 82 participants with nicotine dependence. It compared psilocybin-assisted treatment plus a 13-week cognitive behavioral smoking-cessation intervention with nicotine replacement therapy plus the same behavioral intervention.

The primary endpoint was prolonged, biologically verified cigarette abstinence from the target quit date through the 6-month follow-up, allowing an initial 14-day grace period. The posted counts were 17 of 42 participants in the psilocybin-assisted group and 4 of 40 in the nicotine replacement group. The registry reported a logistic regression odds ratio of 6.12, with a 95% confidence interval from 1.99 to 23.26 and p = 0.003. The unadjusted recalculated risk difference was -0.305 for nicotine replacement therapy relative to psilocybin-assisted treatment, with a 95% confidence interval from -0.480 to -0.130.

Secondary abstinence outcomes were posted for 3-month and 12-month follow-up. The registry also reports adverse event counts, including serious events, by original and crossover groups. Missing-data procedures, analysis populations, the original sample-size rationale, and a multiplicity plan are not reported in the registry record.